What really happened at the DNA level in the experiments in that high-profile CRISPR of human embryos paper from a team led by Shoukhrat Mitalipov at OHSU?

Is the team right that they successfully conducted CRISPR of human embryos to correct a mutant gene, as they reported in their Ma, et al. Nature paper?

Or is the Egli, et al. preprint that came out later in response to the Ma paper more likely to be correct in their implied argument that something else very probably happened instead?

We as a field don’t know yet for sure what molecular events occurred in those embryos, but I believe at this point that the odds are very much that Egli, et al. are right. Hopefully more data will make things clear, but we’ll see. In the meantime, it is useful to think conceptually about what was claimed and place those claims in the context of decades of published biology. That’s what Dieter Egli and colleagues did. More such constructive dialogue and collegial brainstorming about the Ma paper is useful. This kind of process is what science is all about, both pre- and post-publication. If relatively more of it happens prior to publication such as during review, of course, that can save a lot of potential headaches.

The most extraordinary (and fascinating if true) claim made in the Ma, et al. paper was that their use of CRISPR-Cas9 triggered what we might call inter-homolog repair-mediated gene editing and that mechanism was pretty much the only way that CRISPR did its thing in the embryos. What does that mean in English? The idea is that the CRISPR gene correction in the one-cell human embryos was only mediated using the normal maternal chromosome as a template to fix the male chromosome that contained a mutation. If this happened, it is a unique and important finding. However, in their preprint Egli, et al. argued that this proposed phenomenon is very unlikely or maybe even impossible because of the particular spatial nature of chromosome dynamics in the early mammalian embryo.

In that chromosome dance that occurs in the early one-cell embryo, the male and female chromosomes by all accounts remain too far apart to partner up with each other to in turn lead to inter-homologue DNA repair. By analogy imagine two possible dance partners far far away from each other not being able to come together from opposite sides of a ballroom to do a slow dance and engage in conversation. You can’t slow dance with someone 100 yards away, right? Things are going to be even more difficult for inter-homolog repair to occur when the maternal and paternal chromosomes become separated in their own individual pronuclei so in our dance analogy, the two prospective partners would be both far apart and literally in their own bubbles of a sort. It is thought that only much later during metaphase of the first mitosis do the distinct genomes physically interact and if CRISPR acted only at that point or later there could be problems for chromosome segregation and there would almost certainly be more mosaicism.

Mitalipov said a week ago that he still thinks his team is right in an official OHSU statement, but it’s not clear how the CRISPR-Cas9-mediated gene repair could have occurred based on current understanding in the fields of embryology, chromosome dynamics, and DNA repair. So maybe the fields are wrong? That’s not impossible, but the simpler explanation is that the gene editing didn’t happen like they thought.

A new piece from journalist Meghana Keshavan at STAT a few days ago includes fresh quotes from Mitalipov on his team’s paper and the controversy. As quoted in this piece, the first thing that struck me as surprising was that Mitalipov seems very low-key about the whole thing:

“So, I guess this is a pretty startling discovery,” Mitalipov said.

“I actually never knew this would be such a big deal,” Mitalipov said.

“This study has to be tested by time — to learn whether this is a real mechanism or not,” Mitalipov said.

That last quote also suggests much more uncertainty than in the official statement via OHSU. If the central proposed mechanism reported in the Ma paper turns out not to be real, what happens then?

Mitalipov is also quoted there in STAT as trying to explain why others haven’t seen this phenomenon before. Why, for example, in the probably hundreds of thousands of mutant mice made, bred, and studied by researchers over the decades around the world, has no one seen in mice what the Ma paper claims happened in humans? From STAT:

“Mitalipov also has a theory as to why this phenomenon hasn’t yet been seen in other experiments: Most embryonic work is still done in genetically engineered mice. To make good mutant mice, scientists generally target both alleles in a given chromosome — the paternal allele and the maternal allele.

Since both alleles are damaged, there’s no chance for a healthy version to take over and repair (or replace) the broken one. And that, said Mitalipov, may be why no one has previously observed the phenomenon he saw in his lab.

“When you hit both alleles, you can’t see how they repair each other,” Mitalipov said. “So that’s why they never would see it.”

Actually, we generally start with heterozygous (het) ES cells and then het mice. Some researchers more recently are injecting CRISPR-Cas9 into mouse embryos too for gene targeting that could lead to both alleles being mutated, but that’s much less common overall than making and breeding het mice. In other words, we don’t just instantly have all homozygous mutant mice as implied in the above quote.

In addition, the breedings we do should provide plenty of opportunity for maternal correction of mutant paternal alleles, if such a thing was possible. I’ve made quite a few knockout mice and never seen any evidence of spontaneous mutant allele correction. Het x het crosses are the most common we do especially with embryonic lethal mutations, and there would be plenty of opportunity there (and also in Het x WT crosses) for maternal correction of mutant paternal alleles in early embryos (or vice versa). In addition, I’ve never seen anyone else report this kind of spontaneous gene correction via the other corresponding normal chromosome in the germline. Perhaps in his quote Mitalipov was thinking specifically of the kind of mutant mice created using CRISPR in one-cell embryos, which again could sometimes yield two mutant alleles?

Overall, if the early inter-homolog repair between maternal and paternal genomes is a real phenomenon as proposed by Ma, et al., seemingly at least some mouse geneticists would have seen it before and reported it as a novel event, unless it only happens in human embryos and/or only in the context of CRISPR-Cas9. That latter notion of potential CRISPR-Cas9-specificity could in theory be why we haven’t readily seen it in mice, again if it is a real phenomenon. Maybe in the mutant mice to get a spontaneous correction of the mutant gene in question via the corresponding WT allele in embryos, an extra step of a spontaneous DNA double-strand break (DSB) specifically in the mutant allele would be needed to catalyze the process? In the CRISPR context that the Mitalipov team used, Cas9 makes such a DSB at a pre-existing mutant allele. However, in mutant mice in the absence of a nuclease, after the initial mutant allele production phase and during subsequent breedings the mutant allele would not typically then go on to have a new DSB associated with it except in very rare cases, so the embryo may fail to view the gene as damaged and thus not invoke inter-homologue repair? Maybe?

Or maybe in mice, inter-homolog repair does sometimes rarely happen, but we don’t become aware of it because perhaps we just think our mutation didn’t get stably made (or “go germline” as we say), when in fact it was present but then got changed back to WT by inter-homolog repair in one-cell embryos when we bred our initial chimeric mice?

From a bigger picture perspective, inter-homologue repair that evolved specifically for fixing spontaneously damaged alleles in early embryos would risk impairing genetic diversity and leading to loss of heterozygosity. Also, wouldn’t scientists have seen evidence of this in human genetic studies? It should have made for some very unexpected pedigree charts.

Yes, I’m speculating throughout this post and there are a lot of maybes here in trying to model what might have happened in the Ma paper versus what is known from past cell and developmental biology as well as genetics studies. A simpler possibility again is that the Ma paper is just plain wrong, but we don’t know that yet.

Mitalipov has suggested that other labs try to replicate his team’s experiments with human embryos rather than just speculate on what may or may not have happened, but that’s not likely to be easily done. Who else has access to scores or hundreds of human oocytes and/or embryos, and both institutional approval and relevant state and federal laws that allow it? Also, recall that in the U.S. no federal funding can be used for such research and in many other countries there are major constraints or prohibitions on human embryo research. All of this greatly limits possible replication efforts by independent groups.

Unfortunately, the muddy waters related to the claims of the Ma paper aren’t likely to get conclusively resolved one way or another any time soon. A big first step will be to see if the Ma paper team can rebut the concerns of the Egli preprint with new data of their own.

6 Comments

“It is thought that only much later during metaphase of the first mitosis do the distinct genomes physically interact and if CRISPR acted only at that point or later there could be problems for chromosome segregation and there would almost certainly be more mosaicism.”

Do you really think it is far-fetched that inter-homologue repair could have happened during mitosis or the 2-cell stage?

I personally think Egli et al is right too, but this really does seem to be the only possibility that could explain their data.

If that was the case it seems almost certain that Ma, et al. should have also reported seeing a lot of mosaicism. They didn’t.

Also, recombination of this kind during mitosis is thought to be rare and inefficient. Maybe current thinking is wrong in the 1-cell embryo context? Maybe, but unlikely.

Further, Ma, et al. argued for a big difference in outcomes with CRISPR-Cas9 administration during MII versus zygotic introduction; how does that make any sense if repair doesn’t happen anyway until mitosis, much later than either of those stages?

Importantly, if you look at Fig. 3a of the Ma paper (the diagram), they did not claim gene editing happened so late as during mitosis either. Their paper is centered on it all happening earlier, a period when for the other reasons discussed by Egli and in my posts, it seems extremely unlikely.

Unfortunately what could explain the Ma paper’s findings perhaps most simply is what Egli, et al. mentioned: that precise gene editing didn’t take place, but instead that Indels and other issues such as loss of the paternal genome made the authors think it did. I hope that’s not the case, but it seems most likely at this point.

If undetected Indels were fairly common, then that also means another central claim of the paper (the lack of mosaicism) could also be wrong as there may have been a number of embryos mosaic for the Indels. Maybe not, but that also has to be carefully examined.

The problem with these experiments is the requirement for permission to create human embryos for research purposes. I can’t try to reproduce the work, nor can any others I can think of in the stem cell community…the only person who might be able to do so is Dieter Egli and I’m not sure that even he has permission to create human embryos for the sake of research. I think the best solution is for Mitalipov to give Egli the samples for independent analysis. There is precedent for this when Woo Suk Hwang claimed that he had succeeded in somatic nuclear transfer in humans…ironically, while Hwang had to retract his 2006 papers, Mitalipov actually got human SCNT to work in 2013.

I agree with you that if Mitalipov would now allow for independent genomic analysis by 1 or more other labs that would be ideal and could resolve what happened, but that’s unlikely to happen. There may also be tons of pressure on the Mitalipov team to now quickly prove their paper is right or at least not very wrong.

For high-profile papers like these, more rigorous review such as by 4-5 reviewers and independent analyses of samples prior to publication may be appropriate, and in the long actually in the journal and authors’ best interest. The peer and editorial review of this paper at Nature seems to have missed some key questions that would have been better addressed prior to publication than afterwards, to put it mildly.

If interhomologue recombination isn’t occurring, does that count as being “very wrong?” I would say it does.

It’s going to be very hard for one side to prove that the other is wrong, in a definitive manner. Because the premise of Egli et al. is as an “alternative explanation” and not directly proving Mitalipov’s study wrong. Mitosis and 2-cell stage editing leaves a tiny window of chance, even if unlikely. For verification, there might need to be various things like SNPs at the locus Mitalipov et al edited. It might even be that it will not be possible to know with this locus and that additional experiments with other loci will be needed.

It is not unreasonable to assume that there are a few papers on their way. If anything this controversy should elevate the standards for publication of future studies, which is a good thing.

I agree with above, but this is also the problem with “phenomenology” studies. That is, studies in which a phenomenon is reported without a mechanism. I guess this is the trade-off between novelty and certainty…

@L,
As another commenter (Jeanne) mentioned, it’d help clarify things if Mitalipov’s group would give the genomic DNA from their embryo samples to a third party independent lab for analysis, but how likely is that? Things can be resolved pretty clearly if thorough analysis is done including potentially as you said focusing on SNPs and also sequencing with nested primer sets going further and further out from the target gene to scan for Indels.
I fully agree with the concerns about phenomenology studies. At one level someone could argue this Nature paper was too preliminary to have been published without further insights into the mechanisms given how extraordinary the claims.